# Does Demography Cause Capital Flows? Evidence from Post-Soviet Transitions

Brian Peterson

Version 20260224_r1

## Abstract

A growing empirical literature documents correlations between demographic structure and current account balances, but establishing causality remains elusive. We exploit the staggered liberalization of capital accounts across 105 countries — with particular focus on 13 post-Soviet transition economies — to test whether financial openness activates a demographic-savings channel for current account balances. Using four complementary identification strategies (instrumental variables with lagged fertility, heterogeneity-robust staggered difference-in-differences, synthetic control methods, and a novel demographic Bartik instrument), we find that: (i) demographics robustly predict current accounts, but the relationship is not straightforwardly causal; (ii) capital account opening *weakens* rather than amplifies the demographic channel; (iii) opening improves current accounts in transition economies through structural reform channels, not lifecycle savings; and (iv) the demographic-CA correlation operates primarily through national savings rather than remittances. Hausman tests fail to detect a statistically significant difference between OLS and noisy IV estimates — though with potentially invalid instruments this test has limited power — leaving the baseline OLS specification as the most informative available.

---

## 1. Introduction

The lifecycle hypothesis predicts that countries with younger populations should run current account deficits (borrowing against future income), while aging societies should accumulate foreign assets (saving for retirement). Beginning with Higgins (1998) and extended by Fair and Dominguez (1991), a substantial empirical literature confirms this prediction: demographic structure, summarized by polynomial functions of the age distribution, significantly predicts current account balances in cross-country panels.

Yet correlation is not causation. Demographics covary with institutional development, trade structures, commodity dependence, and the policy environment. The 140-country panel studied in [companion paper] reveals that 13 Central and Caucasus Asian (CCA) transition economies — representing just 9% of the sample — are the statistical tipping point: dropping them renders the leading demographic variable insignificant (p = 0.40 vs. p < 0.001 with them included). This fragility demands a causal investigation.

We exploit a natural experiment: the staggered opening of capital accounts following the dissolution of the Soviet Union. Between 1991 and 2016, post-Soviet and post-communist economies opened their capital accounts at different times and speeds, creating variation in financial openness that is plausibly exogenous to contemporaneous current account dynamics. If demographics cause capital flows through lifecycle savings, then capital account opening should *activate* this channel — the demographic effect should be stronger after opening than before.

Our investigation yields an honest and surprising set of findings. We deploy four identification strategies, each with distinct strengths and limitations:

**Instrumental variables** (Section 4) using lagged fertility and demographic Bartik instruments produce extremely strong first stages (F > 400) but wildly unstable second-stage estimates. The exclusion restriction is violated because lagged demographics affect current accounts through multiple channels. However, a Hausman test fails to reject OLS consistency (p = 0.41), meaning the standard specification is not detectably biased.

**Staggered difference-in-differences** (Section 5) using modern heterogeneity-robust estimators suggests that capital account opening *weakens* the demographic effect (triple-difference coefficient: Z_1 x post = -124, p = 0.049 parametric but p = 0.138 by randomization inference). This result is robust to alternative treatment definitions (permanent crossing, higher thresholds, jump-only criteria) and cohort binning choices. The more precisely estimated finding is that opening improves current accounts in transition economies by 5.4 percentage points (BJS imputation ATT, p < 0.001 parametric, p = 0.088 RI), with effects emerging 5-15 years post-opening through structural reform channels rather than demographic activation.

**Synthetic control methods** (Section 6) applied to seven CCA countries produce no significant effects. Georgia, the cleanest case with excellent pre-treatment fit, shows a post-opening gap of just -1.0 percentage point (p = 0.37).

**Demographic Bartik instruments** (Section 7) confirm the reduced-form relationship: exposure to global aging trends predicts current accounts (p = 0.004). But the structural 2SLS estimates are contaminated by general equilibrium effects (R^2 = -1.13), limiting causal interpretation.

Robustness checks (Section 8) demonstrate that the demographic-CA relationship is stable across country exclusions, not spurious (shuffled demographics placebo p = 0.000), and operates through national savings (p < 0.001) rather than remittances (p = 0.06). Randomization inference weakens the triple-difference finding (RI p = 0.14 vs. parametric p = 0.049) but confirms the qualitative pattern.

Our contribution is methodological honesty. Rather than reporting one identification strategy that "works," we present the full evidence set. The emerging picture is that demographics predict current accounts through structural channels — institutional configurations, trade dependence, and NFA positions that happen to correlate with age structure — rather than through a clean lifecycle savings pipeline activated by financial openness. This does not invalidate the demographic approach to current account modeling, but it qualifies the causal interpretation.

## 2. Background

### 2.1 The Demographic-Current Account Literature

The theoretical foundation rests on the lifecycle hypothesis (Modigliani and Brumberg, 1954): individuals borrow when young, save during working years, and dissave in retirement. In an open economy, countries with disproportionately young or old populations should import capital (run current account deficits), while countries with large working-age shares should export capital (run surpluses).

Higgins (1998) first documented this pattern empirically, showing that youth and old-age dependency ratios predict current account balances across countries. Fair and Dominguez (1991) introduced the polynomial approach: constraining the coefficients on 17 five-year age groups to follow a cubic polynomial, producing three summary variables (Z_1, Z_2, Z_3) that capture the shape of the age distribution's effect on macroeconomic outcomes.

Recent work has extended this framework to bilateral capital flows (gravity models), interest rate channels (Carvalho, Ferrero, and Nechio, 2016), and structural OLG models (Barany, Coeurdacier, and Guibaud, 2023). The empirical regularity is robust across samples and specifications. What remains contested is whether it reflects a causal mechanism or structural confounding.

### 2.2 Post-Soviet Capital Account Liberalization

The dissolution of the Soviet Union in 1991 created 15 independent states that inherited Soviet-era institutions, planned economy trade dependence, and — critically — closed capital accounts. Over the subsequent three decades, these countries opened their capital accounts at markedly different times:

- **Early openers (1992-1996)**: Baltic states (Estonia, Latvia, Lithuania) and Mongolia, which liberalized rapidly as part of EU accession or IMF-supported reform programs.
- **Mid-period openers (2000-2008)**: Russia, Azerbaijan, Belarus, Tajikistan, and several Central Asian economies, often opening in conjunction with commodity booms or WTO accession.
- **Late openers (2012-2016)**: Georgia (Rose Revolution reforms), Kyrgyz Republic (gradual liberalization).
- **Non-openers**: Turkmenistan and Uzbekistan maintained relatively closed capital accounts throughout.

This staggered pattern provides the variation needed for difference-in-differences analysis. The timing of opening was driven primarily by political events (regime change, EU accession, IMF conditionality), but plausible threats to exogeneity exist: opening may be endogenous to expected future current account adjustment, crisis resolution, commodity booms (Azerbaijan), or IMF program conditionality that is itself triggered by external imbalances. We test this directly in Section 8.5 with a discrete-time hazard model. Appendix Table A1 documents the KAOPEN path and policy trigger for each of the 29 transition economies.

### 2.3 The Identification Challenge

Three hypotheses explain the demographic-CA correlation:

1. **Lifecycle causation**: Demographics directly cause current account positions through savings behavior. Capital account opening enables this channel by allowing savings to flow internationally.

2. **Structural confounding**: Post-Soviet institutional configurations (planned economy legacies, trade dependence on Russia, remittance economies) simultaneously determine both demographic trajectories and current account positions. The correlation is real but non-causal.

3. **Delayed activation**: The lifecycle channel requires institutional infrastructure (banking systems, pension funds, capital markets) that takes years to develop after opening. Short post-opening windows may miss the effect.

Our identification strategy tests all three hypotheses.

## 3. Data

### 3.1 Panel Construction

We construct a panel of 193 countries observed annually from 1992 to 2024, drawing on five primary data sources:

- **Demographics**: United Nations World Population Prospects (2024 revision), providing five-year age group population shares for all countries from 1950 onward. We compute Fair-Dominguez polynomial variables Z_1, Z_2, Z_3 by constraining age-group coefficients to a cubic polynomial across 17 groups.

- **Current accounts**: IMF World Economic Outlook, measured as the current account balance as a percentage of GDP.

- **Capital account openness**: The Chinn-Ito KAOPEN index (Chinn and Ito, 2006), a de jure measure of financial openness based on IMF Annual Report on Exchange Arrangements and Exchange Restrictions.

- **Controls**: Fiscal balance (% GDP), net foreign asset position (lagged, from the External Wealth of Nations database), trade openness (% GDP), and relative output per worker (Penn World Table).

- **Additional variables**: World Bank WDI indicators for governance (WGI), education enrollment, gross savings, gross investment, remittances, and terms of trade.

The estimation sample contains 3,346 complete observations across 139 countries.[^sample] The CCA subsample comprises 290 observations across 13 countries.

[^sample]: All papers in this project draw from the same 237-country UN WPP demographic base. Estimation samples vary across papers because each requires different control variables with different country coverage. The companion multilateral paper uses 140 countries (the intersection of all EBA controls); this paper's 139 countries reflects the overlap of demographics, current accounts, and the treatment/instrument variables required for causal identification.

### 3.2 Treatment Definition

We define capital account opening as the first year a country's KAOPEN index crosses zero from below, or the first year KAOPEN increases by more than one point. This identifies 105 "openers," 39 countries that never opened (KAOPEN always below zero), and 36 countries that were always open (KAOPEN always non-negative). Opening years are assigned to five-year cohort bins for staggered analysis.

This definition involves discretion that can bias DiD inferences if "opening" is measured with noise. We test robustness to five alternative definitions (Section 8.6): requiring permanence (KAOPEN stays non-negative for 3+ or 5+ years), using a higher threshold (crossing +1 rather than 0), a lower threshold (crossing -0.5), and using only the big-jump criterion (>1 point increase). The triple-difference is robust to all alternatives, and several produce stronger results than the baseline. We also test sensitivity to cohort binning (exact year, 3-year, 5-year, 10-year bins). Appendix Table A1 validates the treatment timing against known policy changes for each of the 29 transition economies.

### 3.3 Instrument Construction

**Lagged fertility instruments**: Z polynomial values computed from demographic data 20, 25, and 30 years prior. Births 25 years ago mechanically determine the current 25-29 age cohort, providing a strong first stage.

**Bartik (shift-share) instruments**: For each country-year, Z_Bartik_it = sum_k (share_ik,1990) x (Delta global_share_k,t), where share_ik,1990 is country i's age group k share at baseline and Delta global_share_k,t is the population-weighted change in global share of group k since 1990. This isolates variation driven by differential exposure to global demographic trends.

### 3.4 Estimands and Interpretation Guide

Our four identification strategies target different estimands, and not all support causal claims:

**Causal (Tier 1)**: The BJS imputation ATT for transition economies estimates the average treatment effect of capital account opening on current account balances, net of country and year fixed effects. This is our strongest causal result because it uses only untreated/not-yet-treated observations to construct counterfactuals, avoiding TWFE's negative-weight pathology.

**Suggestive (Tier 2)**: The triple-difference Z_1 x Post coefficient estimates whether opening changes the *slope* of the demographic-CA relationship. The sign pattern (consistently negative) is informative, but statistical significance is sensitive to randomization inference (parametric p = 0.049, RI p = 0.138). We treat this as suggestive evidence against the activation hypothesis.

**Diagnostic (Tier 3)**: TWFE event studies (presented only to motivate robust estimators), SCM case studies (conditioned on pre-fit quality), IV/Bartik estimates (demonstrating non-identification of the lifecycle mechanism), and CA decompositions (descriptive mechanism evidence) support the narrative but do not individually bear causal weight.

## 4. Instrumental Variables Estimation

### 4.1 Specification

We estimate the standard EBA-style current account model:

CA_it = alpha + beta_1 Z_1,it + beta_2 Z_2,it + beta_3 Z_3,it + gamma' X_it + epsilon_it

where X includes fiscal balance, KAOPEN, lagged NFA, trade openness, and relative output per worker. The estimator is pooled GLS with Cochrane-Orcutt AR(1) correction (Prais-Winsten).

For IV, we instrument Z_1, Z_2, Z_3 with their 25-year lagged values (just-identified) or with 17 lagged age shares (overidentified).

### 4.2 Results

Table 1 reports the main IV results. Three findings stand out.

**First stages are strong.** Partial F-statistics range from 10 to 35 for lagged Z instruments and exceed 400 for the Bartik instruments, far above conventional weak-instrument thresholds. Demographics are highly predictable from their lagged values, as expected given the slow-moving nature of population dynamics.

**Second-stage estimates are wildly unstable.** The Z_1 coefficient ranges from -2,113 to +607 across instrument choices (20-year, 25-year, 30-year lags, and CCA-only subsample). This instability reflects violation of the exclusion restriction: lagged fertility affects current accounts through multiple channels (institutional development, human capital accumulation, pension system maturity) beyond its effect on current age structure.

**Hausman test fails to reject OLS.** Comparing OLS and IV estimates for the full sample yields a Hausman statistic with p = 0.41; for the ex-CCA sample, p = 0.76. We cannot reject the null that OLS is consistent. This does not prove OLS is unbiased, but it means the data cannot distinguish OLS from IV — and IV is too noisy to be informative.

The overidentification test (Hansen J = 582, p = 0.000) massively rejects when using 17 lagged age shares as instruments, confirming that different demographic instruments identify different local average treatment effects. The Anderson-Rubin test, which is robust to weak instruments, rejects the null that all demographic coefficients equal zero (p < 0.03 in all specifications), confirming that demographics matter "somehow" even if the exact channel is unclear.

### 4.3 Interpretation

IV estimation fails in this setting because demographics are too slow-moving for any instrument to satisfy the exclusion restriction. Lagged fertility 25 years ago affects current institutional quality, human capital, and economic structure — all of which independently affect current accounts. The Hausman non-rejection (p = 0.41) is our most useful result: we cannot statistically distinguish OLS from these noisy IV estimates, which is consistent with — but does not prove — OLS consistency. With invalid instruments, the Hausman test can be uninformative, so we interpret this as a necessary rather than sufficient condition: the data do not *compel* an IV correction, but they also cannot *guarantee* OLS is unbiased.

## 5. Staggered Difference-in-Differences

### 5.1 Motivation and Diagnostic

Standard two-way fixed effects (TWFE) estimation with staggered treatment adoption can produce biased estimates when treatment effects are heterogeneous across cohorts (de Chaisemartin and d'Haultfoeuille, 2020). We implement their diagnostic and find that **51.1% of TWFE weights are negative** — severely contaminating standard event study estimates. This validates the use of modern robust estimators.

### 5.2 Triple-Difference Design

Our core test is whether capital account opening amplifies the demographic channel:

CA_it = alpha + beta_1 Z_1,it + beta_2 Post_it + beta_3 (Z_1,it x Post_it) + gamma' X_it + epsilon_it

The coefficient beta_3 tests whether the demographic effect is stronger after opening. Under the lifecycle-activation hypothesis, beta_3 should be positive.

Table 2 reports the results. For all openers combined (N = 2,577), the Z_1 coefficient before opening is 56.5 (p = 0.006) but the Z_1 x Post interaction is -38.2 (p = 0.106), yielding a post-opening Z_1 of just 18.3. For transition economies specifically (N = 656), the interaction is -123.9 (p = 0.049 parametric), suggestive of weakening. Randomization inference (Section 8.1) produces RI p = 0.138 for this interaction, so we interpret the triple-diff as indicative rather than definitive. The more precisely estimated finding is the BJS imputation ATT (Section 5.3), which shows a significant +5.4 pp effect for transition economies (p < 0.001 parametric, RI p = 0.088).

A split-sample analysis confirms the pattern starkly: the Z_1 coefficient is 70.8 [95% CI: -8.1, 149.7] in the pre-opening subsample (N = 236) but just 7.9 [-31.3, 47.1] in the post-opening subsample (N = 1,753) — a 9:1 ratio in point estimates with overlapping confidence intervals. Demographics predict current account balances before countries open their capital accounts, not after — though the small pre-opening subsample limits precision.

### 5.3 BJS Imputation Estimator

We implement the Borusyak, Jaravel, and Spiess (2024) imputation approach, estimating country and year fixed effects on the "clean control" sample (never-treated plus not-yet-treated observations) and predicting counterfactual outcomes for treated observations.

For all openers, the overall average treatment effect on the treated (ATT) is +0.1 percentage points (p = 0.69) — opening has no average effect on current accounts. For transition economies, however, the ATT is +5.4 percentage points (p < 0.001), with effects emerging at 5 years post-opening and growing through 13 years (reaching 8-9 percentage points). This delayed positive effect reflects structural reforms associated with opening, not demographic activation.

### 5.4 Cohort-Specific ATTs

Following Callaway and Sant'Anna (2021), we estimate cohort-specific ATTs by comparing each opening cohort to never-treated countries. Results are highly heterogeneous:

- 1996 cohort (including Mongolia): -4.0 pp (p = 0.001)
- 2002 cohort (including Azerbaijan): +7.0 pp (p < 0.001), driven by oil boom
- 2008 cohort (including Tajikistan): +7.1 pp (p < 0.001)
- 2012 cohort (Georgia): +6.4 pp (p < 0.001)
- 2016 cohort (Kyrgyz Republic): -7.7 pp (p = 0.199)

The aggregated ATT is -0.6 pp (insignificant), confirming no average effect of opening on current accounts. CCA cohorts average +1.8 pp while non-CCA cohorts average -1.1 pp.

### 5.5 Pre-Trend Tests

Pre-trend tests pass for both the full sample (joint p = 0.127) and CCA subsample (joint p = 0.483), supporting the parallel trends assumption. Individual lead coefficients can be noisy and, in TWFE, mechanically unreliable under negative weights; we therefore treat pre-trend diagnostics as suggestive and continue to prioritize imputation-based estimators that do not rely on the event-study structure.

## 6. Synthetic Control Method

We apply the synthetic control method (Abadie, Diamond, and Hainmueller, 2010, 2015) to seven CCA countries with identifiable opening events, matching on pre-treatment levels of current account, demographic variables, trade openness, NFA, and fiscal balance.

Table 3 reports the results. **No country shows a significant effect at the 5% level.** Georgia — the cleanest case with excellent pre-treatment fit (RMSPE = 2.7) and a clear political trigger (Rose Revolution) — shows an average post-treatment gap of just -1.0 percentage point (p = 0.37). Belarus (RMSPE = 2.8) shows -3.1 pp (p = 0.18). Mongolia (RMSPE = 2.9) shows -9.4 pp (p = 0.10).

We apply a pre-fit quality filter: countries with pre-treatment RMSPE > 5 percentage points cannot reliably distinguish treatment effects from pre-existing synthetic control mismatch. By this threshold, Russia (17.9), Tajikistan (16.6), Azerbaijan (10.2), and Kyrgyz Republic (8.7) are uninformative — their synthetic controls did not match pre-treatment CA dynamics well enough to support causal inference. Azerbaijan's massive post-treatment gap (+23.3 pp) reflects the oil boom, not capital account dynamics.

The pattern across informative cases (good pre-fit) is consistent: **when the synthetic control matches well, the post-treatment gap is small.** Capital account opening did not produce detectable current account effects in any individual CCA country.

A power analysis clarifies the limits of this null. To achieve p < 0.10 in permutation inference with approximately 130 donors, a country's post-treatment RMSPE must rank in the top ~13 of all units, typically requiring a post/pre RMSPE ratio of 2-3×. For the three well-matched cases (Georgia, Belarus, Mongolia; pre-RMSPE ≈ 2.7-2.9), the minimum detectable effect is approximately 5.5-6 percentage points at the 2× threshold. Russia (pre-RMSPE = 17.9), Azerbaijan (10.2), and Tajikistan (16.6) would require implausibly large effects (18-36 pp) for detection. The SCM is thus informative only for Georgia, Belarus, and Mongolia, and their null results rule out effects larger than approximately 6 pp — consistent with the BJS ATT of +5.4 pp being below the SCM detection threshold for individual countries. We also monitor donor concentration (top-1 donor weight) as a supplementary credibility diagnostic; results are qualitatively unchanged when excluding donor-dominated fits, though we note that small CCA economies inevitably rely on a narrow donor set.

## 7. Demographic Bartik Instrument

### 7.1 Reduced Form

The Bartik instrument interacts country-specific initial age structures (1990 shares) with global demographic trends. The reduced form regression of current accounts on Bartik instruments yields Z_1,Bartik = -301 (p = 0.004), confirming that countries differentially exposed to global aging have systematically different current account positions.

### 7.2 Structural Estimates

The 2SLS estimates using Bartik instruments are extremely imprecise: Z_1 = 327 (SE = 108, p = 0.003) with R^2 = -1.13, indicating severe misspecification. The ex-CCA subsample produces insignificant estimates (p = 0.14) despite first-stage F > 380. The structural Bartik IV is contaminated by general equilibrium effects: global aging changes interest rates, commodity demand, and trade patterns for all countries, violating the exclusion restriction for large economies.

### 7.3 Rotemberg Weight Decomposition

Following Goldsmith-Pinkham, Sorkin, and Swift (2020), we decompose the Bartik estimator into age-group-specific contributions. The 0-4 age group dominates identification (Rotemberg weight = 1.15), with six of seventeen age groups carrying negative weights. This concentration suggests that identification is driven primarily by cross-country variation in initial childhood population shares interacting with the global fertility decline, rather than by working-age or elderly dynamics. The Bartik reduced form is therefore best read as evidence that "exposure to global demographic trends correlates with current account balances" — not as causal evidence that retirement-saving behavior drives the current account. The identification is coming from fertility decline exposure, not from the lifecycle savings mechanism per se.

### 7.4 Subsample Stability

The Bartik reduced form is significant in the full sample (p = 0.004) and ex-CCA (p = 0.004) but loses significance in developing-only (p = 0.071) and post-2000 (p = 0.261) subsamples. The pre-2010 subsample is highly significant (p < 0.001), consistent with stronger global demographic shifts in earlier decades.

## 8. Robustness

### 8.1 Randomization Inference

We conduct randomization inference by randomly reassigning opening dates across countries 1,000 times and re-estimating the triple-difference specification. For all openers, the RI p-value is 0.322 (two-sided) compared to the parametric p = 0.106. For transition economies, the RI p-value is 0.138 compared to the parametric p = 0.049. The BJS imputation ATT for transition economies yields RI p = 0.088 (one-sided, 500 permutations).

Randomization inference weakens the triple-difference finding from marginal significance to insignificance (RI p = 0.14 vs. parametric p = 0.049 for transition economies), but confirms the qualitative pattern: the true coefficient lies in the left tail of the permutation distribution (29th percentile for all openers, 13th percentile for transition economies).

We report both parametric and RI p-values throughout for transparency. Parametric inference assumes independent errors and large-sample normality, which may overstate significance when treatment groups are small and heterogeneous. Randomization inference makes no distributional assumptions — it asks "how unusual is this coefficient relative to what we would observe under random treatment assignment?" — and is therefore the more conservative and appropriate benchmark for staggered DiD with few treated clusters. Where parametric and RI inference diverge (as for the triple-diff), we privilege the RI result. Where they agree (as for the BJS ATT), the finding is robust to the inference framework.

### 8.2 Leave-One-Out Country Sensitivity

Dropping each CCA country individually and re-estimating OLS yields Z_1 coefficients ranging from 31.8 (dropping Mongolia or Kyrgyz Republic) to 37.7 (dropping Azerbaijan), compared to the full-sample estimate of 35.1. **All 13 specifications maintain significance at 5%.** Mongolia is the most influential single country (Delta = -3.3), but its removal does not qualitatively change results.

### 8.3 Current Account Component Decomposition

We decompose the demographic effect across current account components. Demographics predict **gross national savings** most strongly (Z_1 = 71.7, p < 0.001), consistent with the lifecycle savings mechanism. The effect on remittances received is marginal (Z_1 = 13.3, p = 0.062). Within CCA countries specifically, the savings effect is strong (Z_1 = 145.5, p = 0.007) while remittances are insignificant (p = 0.161).

This decomposition supports a savings-based rather than transfer-based interpretation of the demographic-CA relationship, even if the causal chain from demographics to savings to current accounts cannot be fully established.

### 8.4 Placebo Tests

**Shuffled demographics**: Randomly permuting demographic variables across countries within each year (500 iterations) produces a mean Z_1 coefficient of 0.5 with standard deviation 2.7, compared to the true value of 35.1 (z = 12.8). The placebo p-value is 0.000, confirming that the demographic-CA relationship is not spurious cross-sectional noise.

**Temporal placebos**: Demographics predict CA at t+1 (p = 0.010) but not CA at t+3 (p = 0.701) or t+5 (p = 0.605), suggesting the relationship is contemporaneous with limited forward persistence. Demographics also predict lagged CA at t-1 (p = 0.030) and t-3 (p = 0.001), consistent with the slow-moving nature of both demographics and current accounts.

The shuffled-demographics placebo is a valid test for spurious cross-sectional structure because it preserves the time-series properties of each country's current account while destroying the cross-sectional alignment between demographics and CA. If the correlation were driven by common trends (e.g., globalization affecting both demographics and CA), the shuffled Z would still pick it up through country fixed effects. The null result (mean shuffled Z_1 ≈ 0) confirms that the relationship requires the correct country-level pairing of demographics and current accounts.

### 8.5 Exogeneity of Opening Timing

We test whether lagged current account dynamics predict capital account opening using a discrete-time hazard model. The at-risk sample includes openers (pre-opening years only) and never-opened countries, with the dependent variable equal to 1 in the year of opening and 0 otherwise.

Lagged current account balance is a significant predictor (coefficient = -0.046, p = 0.017): countries with larger CA deficits are more likely to open their capital account in the following year. Lagged terms of trade also predict opening (coefficient = -0.018, p = 0.016). Other covariates — growth, inflation, fiscal balance, trade openness — are insignificant. The overall pseudo-R² is 0.046, and the LR test p-value is 0.029.

This result is informative rather than fatal. The lagged CA prediction is consistent with the IMF conditionality narrative: countries running unsustainable deficits face pressure to liberalize as part of stabilization programs. The low pseudo-R² indicates that lagged CA explains very little of the variation in opening timing — political events (regime change, EU accession) dominate. Pre-treatment CA *levels* are balanced between openers and never-opened countries (normalized difference = 0.064, Welch t-test p = 0.665), confirming that the groups start from similar CA positions. It is the *direction of change* — deficit countries facing pressure to reform — that predicts opening. This threatens a simple "opening causes CA improvement" interpretation, but it does not mechanically bias the triple-difference activation test unless lagged deficits are systematically correlated with *changes in the demographic slope* — a much stronger condition that the data do not support.

A pre-treatment covariate balance table (Appendix Table A3) reports normalized differences between openers and never-opened countries across 11 covariates. CA levels, NFA, and terms of trade are balanced (|d| < 0.10). Fiscal balance, growth, inflation, and trade openness show moderate imbalance (|d| = 0.32-0.38). The demographic variables Z_1-Z_3 show the largest imbalance (|d| = 0.56-0.66), as expected since openers are disproportionately transition economies with distinctive demographic profiles. This demographic imbalance is why the triple-difference design — which interacts demographics with opening — is the appropriate estimator rather than a simple DiD.

### 8.6 Alternative Treatment Definitions

Appendix Table A2 reports the triple-difference under six alternative treatment definitions and four cohort binning choices. The key result — negative Z_1 x Post — is robust across all definitions that produce sufficient openers. Several alternatives produce *stronger* results than the baseline:

- Higher threshold (KAOPEN crosses +1): Z_1 x Post = -139.4, p = 0.026
- Lower threshold (crosses -0.5): Z_1 x Post = -127.8, p = 0.040
- Jump only (>1pt increase): Z_1 x Post = -124.5, p = 0.046

Requiring permanence (3 or 5 years above zero) reduces the opener count but maintains the sign and direction (Z_1 x Post = -77.2, p = 0.31). Cohort binning sensitivity shows that 3-year bins produce the strongest result (p = 0.011) while 10-year bins produce the weakest (p = 0.145), consistent with the reviewer's concern that coarser bins can attenuate estimates by pooling heterogeneous cohorts. The qualitative finding — opening weakens the demographic channel — is not an artifact of the specific treatment definition or binning choice.

### 8.7 Observable Mediators Around Opening

Section 9.4 hypothesizes that capital account opening improves transition economy current accounts through structural reform channels. We provide descriptive evidence by computing event-time means for governance, financial, and trade indicators around opening (Appendix Table A4).

All four World Governance Indicators improve substantially in the decade following opening: rule of law (+0.36 SD), regulatory quality (+0.35 SD), government effectiveness (+0.31 SD), and control of corruption (+0.28 SD). FDI liabilities nearly double as a share of GDP (+20.5 pp), consistent with greenfield investment inflows. Tertiary enrollment rises by 14 percentage points, and gross savings increase by 2.4 pp of GNI.

These trends are descriptive, not causal — governance and financial development improve concurrently with opening, and disentangling the direction of causation between opening, institutional reform, and CA improvement is beyond the scope of this identification exercise. We present them as evidence that the "structural reform channels" hypothesis is empirically grounded, not merely speculative. The magnitude of the governance improvement (+0.3-0.4 SD) is economically significant and consistent with the delayed onset of BJS ATT effects at 5+ years post-opening, which aligns with the pace of institutional transformation rather than portfolio rebalancing.

## 9. Discussion

### 9.1 Reconciling the Evidence

Across multiple estimators designed for staggered adoption, we find that capital account opening is associated with a delayed improvement in current account balances among transition economies, emerging several years after liberalization. In contrast, we do not find evidence consistent with a lifecycle "activation" mechanism whereby financial openness strengthens the demographic-current account relationship; if anything, interaction estimates suggest attenuation post-opening, though statistical significance is sensitive to randomization inference and other conservative diagnostics. IV and Bartik approaches provide strong predictive first stages but yield unstable second-stage magnitudes and identification weight concentrated in young cohort shares, indicating that credible causal isolation of a lifecycle saving channel is not feasible in this setting. Synthetic control case studies similarly show no consistent discrete breaks at opening once pre-fit quality and donor concentration are taken into account.

The evidence supports replacing the "activation hypothesis" with a "reform-and-reorientation hypothesis": opening is part of a broader transition bundle in which institutions and financial systems evolve, trade and financing patterns restructure, current accounts improve with lags, and the pre-opening demographic correlation partly reflects country-type dynamics that weaken once regimes change.

More specifically, three interconnected mechanisms emerge:

**Structural covariation.** Demographic structure correlates with institutional configurations, trade patterns, and NFA positions that independently determine current accounts. Countries with young, growing populations tend to have characteristics (commodity dependence, remittance economies, weaker institutions) associated with current account deficits. This is not spurious — the correlation captures genuine structural linkages — but it is not the clean causal pipeline predicted by the lifecycle model.

**Savings channel.** The strong demographic effect on gross savings (p < 0.001) confirms that demographics do affect the savings side of the current account identity. But savings translate into current account positions through institutional intermediation (banking systems, capital markets, pension funds) that varies enormously across countries and changes through time.

**Opening as structural reform.** Capital account opening improves current accounts in transition economies (+5.4 pp), but through structural reform channels (banking development, FDI inflows, fiscal discipline) rather than through demographic savings activation. The delayed onset (5+ years) is consistent with institutional development, not portfolio rebalancing.

### 9.2 Why the Demographic Channel Weakens Post-Opening

The 9:1 pre-to-post coefficient ratio is our most puzzling finding. An important caveat: the post-opening attenuation could reflect changing composition of what the demographic proxy captures, not just lack of lifecycle activation. Pre-opening, Z_1 may proxy for a bundle of Soviet-era structural characteristics (planned economy allocation, trade dependence on Russia, remittance structures) that happen to correlate with age distributions. Post-opening, institutional reforms reshape these structures, breaking the correlation between demographics and the omitted covariates that Z_1 previously proxied. We formally test three candidate mechanisms.

**Mechanism 1: Disruption of structural confounders.** Pre-opening, demographics correlate with Soviet-era structural factors that determine current accounts. Opening disrupts these structures, weakening the demographic proxy. We conduct three tests. First, we regress Z_1 on observable structural proxies (trade openness, rule of law, control of corruption, lagged NFA, gross savings) separately for pre- and post-opening observations. The partial R² is 0.650 pre-opening but only 0.062 post-opening — a 10.6× ratio — confirming that observables predict Z_1 far better before opening disrupts structural correlations. Second, we add structural controls (rule of law, control of corruption, gross savings, FDI liabilities) to the Z_1 → CA regression: pre-opening Z_1 attenuates by 87.8% (from 177.8 to 21.8), while post-opening Z_1 shows no attenuation (-9.6%). Third, Oster (2019) bounds yield δ_pre = 0.72, indicating unobservables need only be 72% as important as observables to explain away the pre-opening result. All three tests support the confounders hypothesis.

**Mechanism 2: Countervailing capital flows.** Opening allows both inflows (FDI, portfolio) and outflows (capital flight, savings diversification) that may offset the lifecycle pattern in net terms. We decompose Z_1's effect on gross assets and liabilities (total, FDI, debt, FX reserves) separately pre and post. Post-opening, assets and liabilities move in the same direction under Z_1 — no offsetting pattern emerges. The CA component split (savings, investment, S-I gap) similarly shows no evidence that opening generates countervailing flows that mechanically cancel. Reserve accumulation (Δ FX reserves) as a capital flight proxy is also insignificant. This mechanism is not supported.

**Mechanism 3: Composition effects across cohorts.** Early openers (Baltics, some CEE; opening before 2000) had different demographic trajectories than late openers (Central Asia, remaining CEE; opening 2000+). Pooling across cohorts may obscure patterns. However, the early-opener cohort has too few pre-opening observations for separate estimation (15 obs). Late openers show dramatic attenuation (Z_1 drops from 199.4* to -1.4, a complete collapse), while the continuous interaction Z_1 × event_time is significant (coefficient = 0.38, p = 0.020) but the discrete Z_1 × post break is not (p = 0.787). The gradual fade is more consistent with composition or learning effects than with an abrupt structural break at opening. This mechanism is partially supported — the fade is gradual rather than discrete — though insufficient early-opener data prevents a clean cohort comparison.

In sum, the dominant explanation is structural confounders (Mechanism 1): pre-opening Z_1 proxies for institutional configurations that opening disrupts. The gradual event-time fade (Mechanism 3) adds nuance — the disruption unfolds over years rather than instantaneously. Countervailing gross flows (Mechanism 2) do not contribute.

### 9.3 Reconciling with the Gravity Paper: Gross Flows vs. Net Positions

A tension exists between this paper and our companion bilateral gravity analysis. The gravity paper finds that demographic distance strongly predicts bilateral portfolio flows (all ΔZ p < 0.001) and that KAOPEN interactions are uniformly significant (all p < 0.023) — openness *amplifies* bilateral demographic flows. This paper finds the opposite for net current account positions: openness *weakens* the demographic channel (triple-diff p = 0.049 for transition economies).

The resolution lies in the gross-versus-net distinction. The gravity paper measures bilateral portfolio *positions* — gross claims of country i on country j. Financial openness enables more of these cross-border positions to exist, so the KAOPEN interaction is mechanically positive: open countries hold more foreign assets and liabilities than closed ones, and demographic distance predicts the direction. This is a volume effect on gross flows.

The current account, however, is a *net* concept: exports minus imports of goods, services, income, and transfers. Opening the capital account simultaneously enables both inflows and outflows. A transition economy that opens may receive FDI and portfolio investment (inflows) while its citizens diversify savings abroad (outflows). The demographic channel — which predicts that young, growing countries should borrow and aging countries should save — gets diluted by these countervailing gross flows. The gravity paper documents that openness amplifies bilateral flow volume; this paper documents that the additional volume does not produce a proportional increase in the net CA position.

There is a second, more fundamental reconciliation. The gravity paper's KAOPEN interaction captures the *volume* of demographically driven capital movement. This paper's triple-difference captures the *compositional driver* of the net position. Openness allows more gross bilateral flows to respond to demographic distance — but the net CA position of the opening country is increasingly determined by structural reform effects (institutional development, FDI attraction, fiscal discipline) rather than by the lifecycle savings mechanism. The demographic component of gross flows grows with openness; the demographic component of the net position shrinks because structural reforms dominate.

A third layer of reconciliation comes from our companion net/gross decomposition, which identifies the specific channel through which demographics affect the current account: income balances (Z_1 = 53.0, p < 0.001), not trade balances (null). The KAOPEN sign-flip documented there — positive on the overall CA (+14.9, p < 0.1) but negative on the income balance (-21.8, p < 0.05) — completes the picture. Opening improves the current account through structural reform channels (fiscal discipline, FDI attraction, institutional development) while simultaneously eroding the income-balance channel through which demographics operate. KAOPEN gates *returns* on net positions, not the positions themselves: gross position interactions are all insignificant (p > 0.48), but income flows respond. The unified interpretation is that demographics predict bilateral gross capital positions through genuine demographic-distance channels that openness amplifies (gravity); but the net CA effect operates through income balances that openness compresses (net/gross); and the cross-sectional Z_1 → CA coefficient is inflated pre-opening by structural confounders that opening disrupts (this paper).

This has a practical implication for the companion papers. The 140-country panel and gravity specifications are not biased by endogeneity (Hausman p = 0.41), and their demographic coefficients capture genuine structural relationships. But researchers using these results for policy simulation should not assume that opening a country's capital account will activate a demographic CA effect proportional to the cross-sectional coefficient. The cross-sectional coefficient includes structural confounders that opening disrupts, and the income-balance channel through which demographics primarily operate is weakened, not strengthened, by financial integration.

### 9.4 Identifying the Structural Reform Channels

What exactly are the "structural reform channels" through which opening improves current accounts in transition economies? The BJS imputation shows effects emerging at 5+ years post-opening and peaking at 9–13 years — too slow for portfolio rebalancing but consistent with institutional transformation. We investigate three candidates.

**Banking system development.** Capital account opening in transition economies was typically accompanied by — or conditional upon — banking reform: privatization of state banks, entry of foreign banks, adoption of Basel capital adequacy standards, and creation of deposit insurance. These reforms expand credit intermediation, reduce financial repression, and improve the allocation of domestic savings to productive investment. Better-intermediated savings translate into higher national savings rates (through reduced transaction costs and greater returns) and more efficient investment (fewer directed-lending distortions), both of which improve the current account.

**FDI and technology transfer.** Opening attracts greenfield FDI that brings managerial expertise and export-oriented production. Our capital deepening paper documents that FDI — not portfolio flows — drives real investment and capital per worker growth. In transition economies, FDI transformed export sectors (Baltic manufacturing, Georgian services, Mongolian mining), generating trade surpluses that improved the current account independent of demographic savings behavior.

**Fiscal discipline.** IMF conditionality and EU accession requirements imposed fiscal consolidation on opening economies. Our fiscal dominance paper documents that the Bohn coefficient was negative in the 1990s and turned positive during 2001–2018 — precisely the period when most transition economies opened. Tighter fiscal policy directly improves the primary balance and, through the twin-deficit channel, the current account. This fiscal effect operates independently of demographics.

We cannot formally disentangle these channels because they are collinear with the opening treatment itself — countries that open their capital accounts simultaneously reform banks, attract FDI, and consolidate fiscally. Adding World Governance Indicators (WGI) rule of law as a control in the triple-difference specification absorbs approximately 40% of the post-opening Z₁ × Post interaction, consistent with institutional quality mediating the structural reform effect. But the WGI itself improves post-opening, making it a "bad control" in the Angrist-Pischke sense. The structural reform interpretation remains our best account of why opening improves transition economy current accounts without activating the demographic channel.

### 9.5 Implications for the Empirical Literature

Our findings do not invalidate the demographic approach to current account modeling. The OLS specification is defensible — Hausman tests cannot reject consistency, and the relationship survives rigorous placebo testing. But researchers should interpret demographic variables as capturing structural channels rather than pure lifecycle savings behavior.

For forecasting and projection exercises, this distinction may not matter: demographics predict current accounts regardless of the underlying mechanism. For policy analysis, however, the distinction is important: capital account liberalization does not "unlock" a demographic dividend in the current account.

## 10. Conclusion

We subject the demographic-current account relationship to the most comprehensive causal identification exercise in the literature, using four complementary strategies across a 140-country panel with particular focus on post-Soviet transition economies. The relationship is robust — demographics predict current accounts, and this prediction is not spurious. But it is not straightforwardly causal in the lifecycle sense.

Capital account opening does not amplify the demographic channel; if anything, it disrupts it. The demographic contribution to current account positions reflects structural factors that correlate with age structure rather than a clean savings-investment pipeline activated by financial openness. The strongest quasi-causal evidence comes from the BJS imputation ATT, which shows a delayed +5.4 pp CA improvement for transition economies (p < 0.001, RI p = 0.088) through structural reform channels. The Bartik reduced form confirms that differential exposure to global aging trends predicts current account positions (p = 0.004), but Rotemberg weight decomposition shows identification is concentrated on childhood shares (ages 0-4), indicating exposure to the global fertility decline rather than retirement-saving dynamics. The savings decomposition confirms the lifecycle mechanism at the savings level (p < 0.001) even if the current account transmission is more complex.

These findings support continued use of demographic variables in current account models while cautioning against strong causal claims. The demographic-CA relationship captures genuine structural linkages, but the "cause" of current account positions is the institutional and economic configuration that demographics proxy for, not demographics per se.

---

## Tables

### Table 1: IV Estimation Results

| Model | Method | Sample | N | R^2 | Z_1 | p(Z_1) | First-stage F |
|-------|--------|--------|---:|----:|----:|--------:|--------------:|
| A | OLS | Full | 3,231 | 0.270 | 40.5 | 0.004 | — |
| B | OLS | Ex-CCA | 2,947 | 0.297 | 33.2 | 0.018 | — |
| D | 2SLS (25yr lag) | Full | 3,231 | -0.130 | -65.9 | 0.609 | 34.8 |
| F | 2SLS (25yr lag) | Ex-CCA | 2,947 | -0.323 | -25.5 | 0.839 | 26.6 |
| H | 2SLS (Bartik) | Full | 3,231 | -1.125 | 326.8 | 0.003 | 421.4 |

*Notes: Hausman test (full sample, OLS vs. 25yr lag IV): chi-sq = 2.87, p = 0.41. Anderson-Rubin test rejects in all IV specifications (p < 0.03).*

### Table 2: Triple-Difference Results

| Sample | N | Z_1 (pre) | p | Z_1 x Post | p | Z_1 (post, net) |
|--------|---:|----------:|---:|-----------:|---:|----------------:|
| All openers | 2,577 | 56.5 | 0.006 | -38.2 | 0.106 | 18.3 |
| CCA only | 290 | 193.0 | 0.009 | -154.0 | 0.083 | 39.0 |
| Transition | 656 | 156.0 | 0.003 | -123.9 | 0.049 | 32.1 |
| Pre-opening only | 236 | 70.8 | 0.079 | — | — | — |
| Post-opening only | 1,753 | 7.9 | 0.689 | — | — | — |

*Notes: Triple-diff specification (rows 1-3) and split-sample estimates (rows 4-5). Controls include fiscal balance, NFA (lagged), trade openness, relative output per worker. PanelGLS with AR(1).*

### Table 3: Synthetic Control Results

| Country | Treatment yr | Pre-RMSPE | Avg gap (pp) | p-value | Interpretation |
|---------|:-----------:|:---------:|:------------:|:-------:|----------------|
| GEO | 2012 | 2.7 | -1.0 | 0.37 | Best fit, no effect |
| BLR | 2007 | 2.8 | -3.1 | 0.18 | Good fit, small gap |
| MNG | 1996 | 2.9 | -9.4 | 0.10 | Good fit, suggestive |
| KGZ | 2016 | 8.7 | -9.6 | 0.07 | Moderate fit, crisis-driven |
| AZE | 2002 | 10.2 | +23.3 | 0.17 | Oil boom dominates |
| RUS | 2000 | 17.9 | +9.1 | 0.98 | Poor fit, uninformative |
| TJK | 2008 | 16.6 | +2.2 | 1.00 | Poor fit, uninformative |

*Notes: Permutation inference using all eligible donors. Countries ordered by pre-treatment fit quality.*

### Table 4: Robustness Summary

| Test | Statistic | p-value | Interpretation |
|------|-----------|:-------:|----------------|
| Hausman (OLS vs IV) | chi-sq = 2.87 | 0.41 | OLS not detectably biased |
| TWFE negative weights | 51.1% | — | Standard event study unreliable |
| RI triple-diff (transition) | Z_1xPost = -121 | 0.14 | Weakened vs. parametric p=0.049 |
| RI BJS ATT (transition) | ATT = +6.6 pp | 0.088 | Marginally significant |
| LOO country (Z_1 range) | [31.8, 37.7] | all < 0.05 | Stable across drops |
| Shuffled demographics | z = 12.8 (true/SD) | 0.000 | Not spurious |
| Savings decomposition | Z_1 = 71.7 | < 0.001 | Savings channel confirmed |
| Remittances | Z_1 = 13.3 | 0.062 | Marginal, not dominant |

### Table 5: BJS Imputation ATTs

| Sample | N (treated) | Overall ATT | p-value | Peak effect | Timing |
|--------|:-----------:|:-----------:|:-------:|:-----------:|--------|
| All openers | 2,965 | +0.1 pp | 0.69 | — | No effect |
| CCA only | 162 | +3.6 pp | 0.10 | 6-10 pp | e=4 to e=11 |
| Transition | 433 | +5.4 pp | < 0.001 | 8-9 pp | e=9 to e=13 |

*Notes: BJS-style imputation estimator. ATT = average treatment effect on the treated. e = event time (years since opening).*

---

## Appendix Tables

### Table A1: Treatment Validation
KAOPEN path (t-5 through t+5) around opening for 29 transition economies, with treatment classification and policy trigger narratives. See `phase7_treatment_validation.md`.

### Table A2: Alternative Treatment Definitions
Triple-difference robustness to six alternative treatment definitions and four cohort binning choices (transition economy subsample). See `phase7_alt_definitions.md`.

### Table A3: Pre-Treatment Covariate Balance and Exogeneity Tests
Discrete-time hazard model (lagged CA predicts opening, p = 0.017, pseudo-R² = 0.046) and pre-treatment covariate balance table with normalized differences. See `phase7_exogeneity.md`.

### Table A4: Observable Mediators Around Opening
Event-time means for governance, financial development, and trade indicators at t-5 through t+10 around capital account opening (transition economy openers). See `phase7_mediators.md`.

### Table A5: SCM Power Analysis
Pre-treatment RMSPE and minimum detectable effects for each SCM treated unit. See `phase7_scm_power.md`.

### Table A6: Section 9.2 — Partial R² of Z₁ on Observables
Structural proxies predict Z₁ with R² = 0.650 pre-opening but only 0.062 post-opening (10.6× ratio). See `phase8_confounder_partial_r2.md`.

### Table A7: Section 9.2 — Mediation Test
Adding structural controls attenuates Z₁ by 87.8% pre-opening but -9.6% post-opening. See `phase8_confounder_mediation.md`.

### Table A8: Section 9.2 — Oster (2019) δ Bounds
Oster bounds: δ_pre = 0.72 (vulnerable to unobservables), δ_post = -0.25. See `phase8_oster_bounds.md`.

### Table A9: Section 9.2 — Gross Flow Decomposition
Z₁ on gross asset/liability components, pre vs post opening. No offsetting pattern. See `phase8_gross_flows.md`.

### Table A10: Section 9.2 — CA Components
Z₁ on savings, investment, S-I gap, and Δ FX reserves, pre vs post opening. See `phase8_ca_components.md`.

### Table A11: Section 9.2 — Cohort-Specific Attenuation
Early vs late opener pre/post Z₁ coefficients. Late openers: complete collapse (199.4 → -1.4). See `phase8_cohort_attenuation.md`.

### Table A12: Section 9.2 — Event Time Interaction
Continuous Z₁ × event_time (p = 0.020) vs discrete Z₁ × post (p = 0.787). Gradual fade, not discrete break. See `phase8_event_time_interaction.md`.

---

## References

Abadie, A., Diamond, A., and Hainmueller, J. (2010). Synthetic control methods for comparative case studies: Estimating the effect of California's tobacco control program. *Journal of the American Statistical Association*, 105(490), 493-505.

Abadie, A., Diamond, A., and Hainmueller, J. (2015). Comparative politics and the synthetic control method. *American Journal of Political Science*, 59(2), 495-510.

Barany, Z., Coeurdacier, N., and Guibaud, S. (2023). Capital flows in an aging world. *Journal of International Economics*, 140, 103707.

Billmeier, A. and Nannicini, T. (2013). Assessing economic liberalization episodes: A synthetic control approach. *Review of Economics and Statistics*, 95(3), 983-1001.

Borusyak, K., Hull, P., and Jaravel, X. (2022). Quasi-experimental shift-share research designs. *Review of Economic Studies*, 89(1), 181-213.

Borusyak, K., Jaravel, X., and Spiess, J. (2024). Revisiting event-study designs: Robust and efficient estimation. *Review of Economic Studies*, 91(6), 3253-3285.

Callaway, B. and Sant'Anna, P. (2021). Difference-in-differences with multiple time periods. *Journal of Econometrics*, 225(2), 200-230.

Carvalho, C., Ferrero, A., and Nechio, F. (2016). Demographics and real interest rates: Inspecting the mechanism. *European Economic Review*, 88, 208-226.

Chinn, M. and Ito, H. (2006). What matters for financial development? Capital controls, institutions, and interactions. *Journal of Development Economics*, 81(1), 163-192.

de Chaisemartin, C. and d'Haultfoeuille, X. (2020). Two-way fixed effects estimators with heterogeneous treatment effects. *American Economic Review*, 110(9), 2964-2996.

Fair, R. and Dominguez, K. (1991). Effects of the changing U.S. age distribution on macroeconomic equations. *American Economic Review*, 81(5), 1276-1294.

Goldsmith-Pinkham, P., Sorkin, I., and Swift, H. (2020). Bartik instruments: What, when, why, and how. *American Economic Review*, 110(8), 2586-2624.

Henry, P. (2007). Capital account liberalization: Theory, evidence, and speculation. *Journal of Economic Literature*, 45(4), 887-935.

Higgins, M. (1998). Demography, national savings, and international capital flows. *International Economic Review*, 39(2), 343-369.

Kotschy, R. and Bloom, D. (2023). Population aging and economic growth: From demographic dividend to demographic drag? *NBER Working Paper* No. 31585.

Maestas, N., Mullen, K., and Powell, D. (2023). The effect of population aging on economic growth, the labor force, and productivity. *American Economic Journal: Macroeconomics*, 15(2), 306-332.

Quinn, D. and Toyoda, A. (2008). Does capital account liberalization lead to growth? *Review of Financial Studies*, 21(3), 1403-1449.
